Research ideas, part 3: Ask questions

I’m fascinated by the television show Shark Tank, where professional investors listen to a brief pitch from aspiring entrepreneurs, ask a few questions, then make a decision on the spot to invest (or not invest) up to millions of dollars in an idea. Similarly, if you’ve ever pitched project ideas to someone who has been doing research for a significant amount of time, they can often tell you very quickly whether they think your idea has promise.  It may seem as if these people are “going with their gut” as they make decisions, but I can almost guarantee that this is not the case, and that each decision is the result of a systematic and calculated evaluation process. These individuals have just practiced it enough that it becomes almost instantaneous.

You might be tempted to think that if you’re not giving away millions of dollars on Shark Tank, then you don’t need this ability to quickly judge the merit of ideas.  Not so.  As we discussed previously, if you are in or aspiring to a research career, you need ideas, and to have good ideas, you need to have a lot of ideas.  This means that you need to be able to quickly evaluate each idea and decide if it is worth the investment of your time to develop further.  There are many ways to do this – our process involves a series of questions:

• Has this exact thing already been done? This may seem obvious, but it’s surprising how tempting it can be to put off asking this, as it is the one question that can completely kill an idea.
• Is there a real problem or question here? Is there something that we don’t know or can’t do? Is that thing potentially impactful?
• Have others worked toward solving this problem or answering this question? This is a subtler version of the first question – maybe nobody has done exactly what you are thinking of doing, but likely someone has reported a technology to help meet the need or data toward an answer to the research question. If the answer to this is “yes,” then ask whether there are still limitations to the reported approaches or knowledge that is missing. Will your idea help overcome that?
• Is this really the best way to solve the problem or answer the question? This can be a tough question to answer honestly, as we often become so enamored with our approach that we don’t want information that would compel us to let go of the idea. A productive way to push through that discomfort is to ask: If there is a better way, what is it? Has that already been done? Would I be excited to work on the “better” idea?
• Is this feasible? It may seem odd that this question is coming so late in the game, but that is intentional. If you realize at this point that there is a feasibility challenge, it is likely that you can find a creative solution to reduce risk, then keep going.  However, if you spend significant time up front convincing yourself of feasibility only to later realize that the idea is not significant or impactful, that’s not an ideal situation.

When you’re starting out with generating research ideas, it may take quite a bit of time to think through these questions. The good news is that as you practice and gain experience, you will become much more efficient, and likely gain the ability to triage most ideas within seconds of generating them.

The questions above are aimed at deciding whether an idea has enough merit to warrant a plan. If you’ve gotten this far and haven’t killed the idea yet, it’s time to start asking some more practical questions: 

• What is most likely to go wrong? This question is in line with the “fail fast” philosophy – if something isn’t going to work out, that’s fine, but you want to find out sooner rather than later. As logical as that sounds, it can be tough to act on. Again, it’s important to push through the discomfort, figure out what is most likely to cause a complete failure of the project, and develop a strategy to run at that answer.
• If things do go wrong, what are the alternative approaches? Pretty self-explanatory, but it’s never too early to start thinking about this!
• If nothing works, what can I still learn or produce? While you obviously hope not to end up in this situation, sometimes that’s just where research takes you, even with a really good project idea.  It’s important to think ahead about whether you could “turn lemons into lemonade.” If the answer is that nothing can be learned or produced if things don’t work, the project might still be worth trying, but at least acknowledge that risk up front, and set a timeline for how long you’re willing to commit before you succeed or drop the project. 

If my group and I can make it through this entire series of questions and still have a high level of enthusiasm for an idea, then we recognize it’s something we should give serious consideration to, and we already have the start of a strategic plan to get going!  Stay tuned for next month, where I’ll close out this series with some practical tips for what to do with the ideas that successfully make it through this mental gauntlet.

Think of a key question that I missed? Use a totally different process? Share that in the comments!

Research ideas, part 2: This could get ugly

I have a lot of bad ideas. Literally thousands of them. Not just bad, but terrible ideas. And, they are the secret to my success in this job.

As researchers, ideas are what fuel our progress. This fact is both exhilarating and intimidating, and where you lie on that spectrum of emotions is probably closely tied to how reliable of a process you have for generating and developing your ideas. Last month, we confronted the fallacy that generating ideas is a “magical” process of waiting for inspiration to strike, and we explored systematic ways to produce ideas. But, if you do research, you know that having ideas isn’t enough – you need to have good ideas.  This month, we’ll confront a second fallacy – that this process involves brilliant people generating brilliant ideas on the first try.

Adam Grant is a Professor of Management at the Wharton School, where his research includes studying the hallmarks of creativity.  One conclusion that he draws from his work is that “The more output you churn out, the more variety you get, and the better your chances of stumbling on something truly original.” In other words – if you want to have good ideas, you need to have a lot of ideas. And, chances are that if you have a lot of ideas, you are going to have a lot of bad ideas.

How then, do we separate the few good ideas from the overwhelming excess of bad ideas? Next month, I’ll dive into the specifics of this process, but before we get there we need to start with the obvious first step – you need to be willing look closely, even though most of what you see is going to be ugly.

While crucial, this step is surprisingly difficult.  Why is that?  The easy answer is that you might feel like you’re wasting your time looking at bad ideas. I want to challenge you to consider some other reasons you might find this task difficult (I can list these because I struggle with every one of them):

• If my idea is bad, I’ll feel unintelligent
• If other people see my bad idea, they will think that I’m unintelligent
• If this idea is bad, it might mean I’m just bad at coming up with ideas and I will never have good ideas
• The stakes are high – I am relying on my ideas to secure a fellowship or grant, a job, or tenure 

Now that we’ve got all that out in the open, how do we move forward? A big part of the answer lies in how you view your abilities and intelligence.  Carol Dweck, a renowned Professor of Psychology at Stanford, hypothesizes that there are two ways that we can view our intelligence and abilities:

Fixed mindset: Intelligence and talent are fixed traits that are set at birth.  These factors alone determine the level of success you can achieve.

Growth mindset: Intelligence and talent are just the starting point and can be improved thorough hard work. Effort and persistence result in growth, which leads to success.

A detailed unpacking what this means for us as researchers and people is a topic for another blog post, but hopefully you can see the difference that this makes in how you approach your bad ideas.  From the fixed mindset, having bad ideas not only judges your current abilities, but also defines your future potential for success (or lack thereof). That’s terrifying! In contrast, the growth mindset allows you to take an honest look at both the good and bad, as you know that there is a path forward to improvement, no matter what your starting point or the bad ideas you have along the way.

Another way to think about this is to view doubt as an essential step in the creative process.  Adam Grant highlights, “…there are two different kinds of doubt. There's self-doubt and idea-doubt. Self-doubt is paralyzing. It leads you to freeze. But idea-doubt is energizing. It motivates you to test, to experiment, to refine…” The fixed mindset traps you at self-doubt, whereas the growth mindset allows you to skip over this step and focus on idea-doubt.

Next month, I’ll discuss the process that we use to evaluate and refine our ideas, with the goal of quickly discarding the bad ideas and focusing our energy on making the good ideas better. In the meantime, spend some time observing how you think about your ideas – when a new idea pops into your head, do you race to look closely and investigate the potential weaknesses, or do you hide it away to think about later? Challenge yourself to push toward a growth mindset and see if this makes a difference.  The faster you can move through the bad ideas, the more quickly you will find the good ones!

Have thoughts or experiences you want to share? Think my approach to this topic is itself a bad idea? Leave a comment and let’s discuss!

Research ideas, part 1: It’s not magic

As researchers, ideas are arguably our most valuable form of currency, and generating new ideas is a requirement for becoming an independent scientist. However, relatively few resources are available to offer guidance on this process.  Early in my career, I thought that generating ideas was a magical process where I had to wait for inspiration to come to me. However, over time I’ve come to appreciate that it really can be a systematic and reliable practice.  In this series of blog posts, I’ll outline how to generate ideas, how to vet and refine those ideas, and how to manage all of the thoughts and information that you gather along the way. This month, it seems only right to start at the beginning with the question: Where do research ideas come from?

Nothing is new. A key misconception in generating research ideas is that you need to create something entirely new out of nothing.  But, the fact is that almost nothing in the realm of research ideas is completely new.  Even in the rare instances that scientists uncover something truly novel or unexpected, it is usually because they were looking for something else based on existing knowledge. Recognizing this frees us up to think about how we can build compelling ideas by embracing the foundation of current knowledge or technology.  In my view, there are four different approaches for this construction process:

• Apply: Can I use an existing technology or approach to address a different unsolved problem or unmet need in science?
• Elaborate: Is there something important that this technology can’t do? Can I think of a different approach that could fill that gap?
• Connect: Is there a connection or potential synergism between these technologies, theories, or ideas that nobody has realized yet?
• Explore: Is there something important that we don’t yet know or understand? Is there a way to gain the missing knowledge? What could we do once we have that knowledge?

Every moment is an opportunity for inspiration. As I mentioned above, a second key misconception that I used to struggle with is the idea that I had to carve out “idea generation time” and then sit and wait passively for inspiration to strike (or not strike) me. While it is a great practice to have dedicated “thinking time” set aside in your schedule, most ideas strike when we are actively doing something.  This goes hand in hand with the realization that nothing is new.  If most ideas are going to build upon the foundation of existing knowledge or technology, then ideas are most likely to bubble up when you are actively engaged with the world around you. The great news about this is that almost all parts of your day can be turned into “idea generation time.”  A few of my favorite opportunities for inspiration have included:

• reading the literature
• listening to seminars or conference talks
• working in lab
• talking with colleagues
• talking with non-scientists
• everyday life activities – exercise, shopping, driving
• sleeping…?

If you are new to the process of generating research ideas, I hope that this framework does a bit to demystify the process and get you started. Multiplying the diversity of types of ideas with the numerous opportunities for inspiration, it becomes clear that even in an average day, you can generate a lot of ideas! That is encouraging, but can also feel overwhelming. Next month, we’ll discuss why this high quantity is necessary for achieving high quality with your research ideas, and how to confront the challenges that it can pose.